Scientific Research: A Hitchhiker’s Guide to a Destination that is not yet on the Map*
The Point of Departure
Scientific research starts with the curiosity to learn and the desire to create knowledge. Research is not only about publishing articles or even, as some purists understand it, thinking about disinterested and beautiful concepts. It is also about its impact on society and a systematic approach to solving real-life problems. For example, in technology-related research the objective if often to innovate, become entrepreneur and see how your curiosity shakes the real world around you. Or make a vaccine and de-paralyze the world in record time. At some point the research career may become a maelstrom of citation-hunting, research funding, prestige, and a nagging, almost comical, “I do not have time for research because I am overwhelmed with administration and management”; however, it is the curiosity and creation of new knowledge that still shelter the magic of research.
A person that is about to start with the research career, should get ready about the obstacles and frustrations. Nevertheless, to avoid the effect that "the grass is greener in the other laboratories", it would at least be good to know: What are the ideal conditions to do research, and specifically PhD? Here are four of them:
- You are sufficiently undisturbed to do what you find interesting. Here undisturbed means that you are not constantly and randomly showered with teaching and administrative tasks. One cannot and should not escape other tasks entirely, as one learns a lot from those as well. Therefore, the keyword above is "constantly and randomly", which means that you can find undisturbed time to think, read, write, analyze, make experiments, etc.
- There are dozens of fellows/peers in a similar position you can talk to. This is not so much to use them as a benchmark to see how good (or not) you are, but more as partners for dialogue, exchange of ideas, or even mutual coaching. The superpowers that your peers have can be different from your superpower and you can help each other a lot. I have seen the cases in which wizards of math or theoretical analysis teaming with wizards of simulation and experiments, leading to great results.
- There are supervisors to get support from. Besides support, the most important thing you can get from your supervisors (and your peers as well) is a well-intentioned, but sharp critic. It is always better that your supervisor rejects your paper now, rather than the same paper being rejected three months later by anonymous reviewers, and often for the same reasons provided by the supervisor.
- You are actually getting salary for doing research or a PhD. This is not a rule, there are countries where you need to pay for your doctoral studies.
For example, a good approximation of these conditions is a doctoral position within a Marie Curie Innovative Training Network (ITN), where one gets employed as a doctoral student along with 10+ other people, in different institutions, and there is a whole network of peers and supervisors that can be relied upon throughout the doctoral studies.
Three Simple Truths in Research
The simplest truth we seem to constantly forget in research is that one needs to be different from others in a way that makes sense and is relevant. We often get the drive go the same was as the others: "Everybody works on Machine Learning, data and Artificial Intelligence, so I have to do that as well". However, it would be more meaningful to start from "This is the problem I want to solve and my hypothesis is that Machine Learning can help; if it does not help, I have to find another approach". Being different is difficult and requires creativity, being the same pushes towards conformity. It is easier said than done, as we are all conforming to popular areas, but in doing that we should not neglect the simple truth that, in the end, we have to create something that is different.
The second one is related to methodology-driven vs. problem-driven research. Having a specific methodology and trying to find a problem is often negatively characterized by "having a hammer trying to see everything as a nail". In fact, this approach is not necessarily bad, as it can provide some balance for the approach that is oriented purely towards grand, interesting problems. Finding some good nails can keep the scientific production and motivation, especially if the grand and interesting problem is intractable. This is nicely illustrated in the book "Uncle Petros and Goldbach’s Conjecture: A Novel of Mathematical Obsession", where a brilliant mathematician spends his whole life working on the deceptively simple Goldbach conjecture without finding a solution.
Finally, there is the truth about the tragedy of the commons and how a popular topic gets quickly depleted. To illustrate the tragedy of the commons, consider a young doctoral student that publishes an article and starts a new field; after a short time some big labs notice it and often reap the highest citation gains from that topic. Then the number of researchers working on that field explodes and the field becomes saturated. This is reminiscent to the stock market, where a small investor gets notices a good stock and buys it, but only big investors can drive the price up and reap the highest gains of that stock; buying the stock when the price is high is not profitable. Rather running into the tragedy of the commons, a sustainable research strategy relies on finding concepts and ideas that produce new green fields, as illustrated on the figure below.
Why is Research Similar to Jazz Music
In jazz music one starts by learning some basic progressions. This is followed by practicing A LOT of scales and chords and listening to A LOT of music. At some point one starts to recognize the main ideas, the signatures of different masters, the combinations they use and the new things they bring. It is very important to imitate the masters and to improvise, and each improvisation brings a piece of new music. After a while one can reach great results, even a new direction in music and become a symbol of innovation, as is, for example, Miles Davis. Finally, even the wider public, not usually interested in esoteric jazz ideas, starts to appreciate the accomplishment and the impact; the picture below is of Thelonious Monk, a towering figure of jazz.
To start the analogy, in research one starts by learning the basic principles and theories, reading A LOT of general and essential books in the field. For example, in communication engineering these books are in probabilistic modeling, optimization, etc. Then one continues to read A LOT of scientific articles; they are often difficult to understand and one needs to read them twice or five times until some understanding starts to emerge. This is accompanied by practicing: sketching small problems, simulating simple systems, trying out small ideas, many of which will fail. The first works/articles one writes are usually based on imitation of other articles. In this sense it is better to find the real masters and imitate them, "improvising" on a given theme and thus adding the necessary level of novelty. At some point this improvisation is sufficiently different from those one imitates and — voilà, a new research article comes out. After a while one can reach great results, even a new research area and become a symbol of new thinking, as is, for example, Niels Bohr. Regarding the accessibility and usefulness to the wider public, the prime example is the recent mRNA vaccine for COVID-19, developed in a record time based on research and ideas that have been developed since the 90s, initially met with a lot of skepticism. A notable example in communication engineering is Qualcomm, founded by Irwin Jacobs and Andrew Viterbi, each of them with a stellar track record in theoretical research: Viterbi has an algorithm named after him, while Jacobs is the co-author of one of the best-ever books on communication engineering.
Thinking about Modeling and within Models
The model is our representation of a real-life scenario that helps us to grasp the problem, think of its features and outline possible answers. Think of a model as being a caricature of reality, but, as every good caricature, it contains sufficient features to recognize the person or the situation it deals with; this is the case with the model of a person on the picture below.
We use models consciously and unconsciously in our daily lives in order to deal with the complexity of the world around us and simplify the things to achieve comprehensibility or, simply, optimize the time and energy used for thinking. However, these everyday models should be used with caution, as their non-critical use can lead to prejudice and, for example, unfair judgement of a group of people. Used properly, the models can lead to understanding, new insights into existing concepts and to completely new ideas.
Making a proper model that contains a sufficient level of details, but still not to many, is almost a work of art. Modeling is the place where one should stick to Einstein's quote: "everything must be made as simple as possible, but not one bit simpler." Sometimes the details enhance the model, and sometimes they blur the big picture. Let us take an example from communication engineering. Let us say we make models for propagation of radio signals in wireless communications, such as Wi-Fi, and we want to model the influence of people in a room in terms of how their presence impacts the signals. In this context, the question “what is the color of the sweaters that people wear” is rather irrelevant for the problem at questions, as the frequencies of the radio signals are not affected by the sweater color. However, once we consider wireless communications based on visible light (Li-Fi), then this question ceases to be silly and may become a useful addition to the model: people in white sweaters will cause more reflection of the light signals and potentially lead to a different level of interference.
Reading of Research Papers
There is always a certain tension between learning more by reading what the others have done and producing research yourself. Richard Hamming, the famous coding theorist, in his article “You and Your Research” tells the story of a colleague who was constantly preparing for research by reading and was not feeling ready to start doing actual research, publishing, or patenting. “I knew there would be no phenomenon or effect that would bear his name,” Hamming said. I read Hamming's article at the start of my graduate studies and it was an important motivation to take the first step into creating something, despite the feeling of not knowing enough. The interplay between reading and creation of research results of your own is essential: you will probably hit a wall somewhere, you will find yourself in the dark, but in the end you will succeed in creating new knowledge.
Here is a biased personal view how to read scientific engineering papers. If it is an unknown field, something completely new, I first read the introduction and the context, then the descriptive part where the authors say what they do differently from what has been done before. If that is sufficiently interesting, then I take a deeper dive. If the paper is in an area that is familiar, I go to the section where they describe the problem and the model, to understand exactly how the paper is addressing the problem. This is the place where I expect to see the intellectual leap, how the authors have introduced new thinking. The last thing I look at are the results, because my assumption is, since it is published, there must have been credible results.
Finally, I want to emphasize that when one reads a good work in engineering, language and style are not secondary. It is definitely good to read from areas that are broader than the concrete subject matter of research interest. Good ideas are like pearls that can be recognized even in a field that is unknown, provided that they are written eloquently and with the intention to create understanding, rather than intention to intimidate the reader ("look how difficult are the things that I can do").
Thinking through Writing
Besides being necessary to come to arrive to a stage to publish an article or a book, writing is indispensable for structuring the way one thinks about a research problem. Recall the effect that occurs often when one reads a complex, difficult article: you read it once quickly and you realize that you did not understand anything; however, when you go back to re-read it, you realize that you have already picked up some things and ideas, but you were not aware of it before re-reading. I am sure there is an appropriate learning theory that covers this heuristic observation; here I am just using to draw similarity to the writing-thinking process. One thinks about an idea and writes down some notes. The next day she reads the idea that yesterday-her was excited about and it sounds different, requires corrections, maybe it is not exciting anymore or gives a perspective to a completely new direction. Once a person is forced to write down the ideas, those ideas get a life and impact on their own.
After many rounds of writing and revising, one comes to a nicely packaged "product", of which the first writeup of the idea is a faint, rudimentary version. Take, for example, the mathematical proofs. When one reads them in a book or an article, they look perfect, but it is like seeing the food that is finally served in the restaurant and not thinking about the work in the kitchen; the proofs certainly did not look enviably perfect in the early versions.
Here I reiterate the final point from the "reading" part above: write in a way to make it understandable, educate and inspire others, rather than intimidate the others about how complicated are the things that you can do.
Publishing and Co-Authorship
What we are doing research on should, of course, eventually be published. A publication is like scoring a goal in a football game: over a longer period the result is remembered and very rarely how well a goalless draw had been played. In other words, you may enjoy the process and the well-playing (which is, in fact very important), but over a long run the results and publications count, as various employers, funding agencies, and committees do not have a reliable way to assess how much you have enjoyed the process.
Regarding the publishing tempo, there are people who want to make one publication a year, but such one that it changes the world. This is quite risky and something we have invested time and energy may look to us as world-changing, but not so much so according to objective criteria. Differently from this, there are researchers that have hundreds of publications a year. Of course, many of them are co-authored, which raises the question of what it really means to be a co-author. My rule-of-thumb criterion is that a co-author is the one that contributes a part without which the research result or the final article could not have happened. Sometimes this can be a tiny, but very lucid change of the model; other time it can be an elaborate experimental work.
Some further remarks on authoring and co-authoring of scientific papers:
- Having a co-author can be a real blessing, since the constructive criticism from the collaborators is the most important. If the co-author has arguments to tell you that your paper is not ready and that you should not send it, then the co-author is doing you a great favor.
- Maintain the publication pace, since it is remember to score goals (sic) along with playing well. It is difficult to fully contribute to one paper in all aspects, and to work on papers in parallel with more people, but here you have to find your own optimal regime. However, always keep in mind the Vancouver Convention about the requirements for authoring and co-authoring papers.
- Take initiatives for new publications. It is good to join in publications and as a side player, you do not have to be the leader all the time. As an academic researcher it is always good to work on at least two or three ideas in parallel; this mitigates the risk that the idea will not work or that someone else from another research group (hopefully not down the corridor in your same institution) has done exactly the same.
- Write down things almost every day. The comedian Jerry Seinfeld wrote new jokes every day — some of them turned out good, others great, and third ones did not work out; however, it is important that he produced them all the time. Recall the argument from above about thinking through writing.
Some final Thoughts
Besides producing results and articles for the peers, there is an information from our research that can be of significant public interest. That is the case, for example, with information on the pandemic and vaccines, climate change or, in the case of communication engineering, 5G and the related misconceptions. Although they do not count as peer-reviewed scientific article, popular articles or videos have a significant societal duty to bring reliable knowledge to the general public and help to spread misinformation. The hitchhiking starts with curiosity, but, regardless of the research destination, it should eventually give back to the society.
*Note: Some time ago I was asked to give a talk to a group of just started PhD students, working at the intersection of wireless communications and machine learning. This is a good opportunity to reflect on some important topic that are underlying scientific research and graduate studies. A different version of this article in Macedonian language can be found here.
